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BIOSTATISTICAL METHODOLOGY IN CLINICAL

TRIALS

Guideline Title Biostatistical Methodology in Clinical Trials

Legislative basis Directive 75/318/EEC as amended

Date of first adoption May 1993

Date of entry into

force

October 1993

Status Last revised May 1993

Previous titles/other

references

B i o st a t i s t i c a l me t h od o l og y i n c l i n i c a l t r i a l s i n a p p l i c a t i on s

f or M a r k e t i n g A u t h o r i sa t i o n s f or M ed i c i n a l P r o d u c t s /

I I I /3630/92,

Additional Notes This note for guidance concerns the application of Part 4,

sections C and F of the Annex to Directive 75/318/EEC as

amended with a view to the granting of a marketing

authorisation for a medicinal product. It is intended to

give support to applicants when designing, conducting,

documenting, evaluating and reporting clinical trials of

new medicinal products in the context of their overall

clinical development. It is written primarily to

harmonise the biostatistical methodology applied to

clinical trials within member states, during both clinical

development and subsequent review.

CONTENTS

1. INTRODUCTI ON

2. OVERALL DEVELOPMENT CONSIDERATIONS

3. CLINICAL TRIAL DESIGNS

4. OTHER DESIGN ISSUES

5. THE SAMPLE SIZE

6. THE POPULATION

7. DESIGN TECHNIQUES TO AVOID BIAS


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8. PRIMARY AND SECONDARY VARIABLES

9. THE CASE REPORT FORM

10. PRE SPECIFIED DATA ANALYSIS

11. THE CONDUCT AND MONITORING PHASE

12. INTEGRITY OF DATA AND COMPUTER SOFTWARE

13. EVALUATION AND REPORTING

14. OUTLINE OF SAFETY ISSUES

15. SUMMARISING THE CLINICAL DATABASE


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BIOSTATISTICAL METHODOLOGY IN CLINICAL

TRIALS

1. INTRODUCTION

This n ote for gu ida nce should be rea d in th e light of Directive 75/318/E EC a s a mended w hich

sets up the relevant regulatory framework. I t should also be read in conjunction with note for

guidance on Good Cl in ical Pr act ice(GCP) and which emphasises the importance of stat ist ical

principles and expertise in the design, conduct and analysis of cl inical tr ials .

This Note is int ended to give support to a pplicant s w hen desig nin g, condu ctin g,

documenting, eva lua ting a nd report ing cl inical tr ia ls of new medicinal products in the

context of their overa l l cl inica l development. I t wi l l a lso a ssist scient i f ic experts cha rgedwit h prepa ring Expert Reports or a ssessing evidence of ef f icacy and sa fety, principal ly f r om

Phase I I I cl inical tr ials . I t is wri t ten primari ly to harmonise the biostat ist ical methodology

applied to cl inical tr ia ls within member sta tes, during both cl inical development a n d

subsequent review. I t is la rgely concerned with plan ning a nd methodology, a nd does not

at tempt to cover systema tical ly the structure a nd content of cl inical reports w hich is covered

in th e note for guida nce on Str uctur e and Content of Cli ni cal Report s.

The ef f ica cy a nd cl inica l sa fety of medicina l products must be demonstra ted by cl i n ica l

tr ia ls which fol low the guida nce given in G CP . Within this document biosta t ist ical is sues

a re clea rly ident i f ied as a n int egra l part of the design a nd conduct of cl inical tr ia ls .

B iosta t ist ica l principles underl ie the mult i-discipl inar y a pproach necessa ry to ensure that

clinical t ria ls provide adeq ua te evidence to support the decisions wh ich r est upon them a n d,

therefore, an appropriately qual i f ied and experienced stat ist ician should be responsible for

each cl inical tr ial at al l s tages f rom design through to reporting.

In the early phases of product development many cl inical tr ials are of an exploratory nature.

Some of the cont ent of th is note is str ictly releva nt only to confir ma tor y tr ials such a s the

pivota l tr ials carried out in th e la ter phase of development ( la te P ha se I I /P ha se I I I) in order

to give def ini t ive proof of ef f ica cy, a nd t hese tr ia ls a re certa inly the ma in ta rget of the

stat ist ical material covered here. Nevertheless, biostat ist ical considerat ions are relevant to

a l l cl inical tr ia ls ; hence the substa nce of this note sh ould be applied a s far a s possible to a l l

pha ses of product development a nd t o a ll types of study . In section 14 of this note for g ui da nce

a brief outl ine of some of the sta t ist ical issues relevant to sa fety evalua tion is gi ven .

However, a separate guideline will be necessary to cover this topic fully.

This note for guidance is intended:

to outl ine the relevant principles of design and analysis ,

to describe generally appropriate approaches to these tasks,

to describe some a pproa ches which should not be ad opted,

to set conventions w here choice would otherwise be entirely a rbi tra ry. I t is not int ended

to give deta iled (textbook or cookbook) specifica tion of meth odology, thus le a vi n ga pplica nts a nd other users responsible for m a king reas oned choices between


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a l terna tive stat ist ica l approa ches an d procedures to solve speci f ic problems. This m a y

sometimes require innovation.

All importan t deta i ls of the design, conduct a nd proposed a na lysis of ea ch cl inical t r ia l

contr ibuting to a ma rketin g a uthorisat ion applica t ion should be clear ly speci f ied in a

protocol wr itt en before the tr ia l begins. Any subsequent cha nges to the protocol, a nd the

reasons behind them, should be car eful ly documented. The cl inical tr ia l protocol and a l l

subsequent a mendments should be signed an d dat ed by the responsible personnel ( incl ud in g

the t r ial st a t ist icia n). The tria l sta t ist icia n should ensure tha t the protocol covers a l l relevant

stat ist ical issues clearly and accurately, using technical terminology as appropriate .

Although this note for guidance is wri t ten largely f rom the class ical (f requentist ) viewpoint ,

the use of Bayesian or other well-argued approaches is quite acceptable.

2. OVERALL DEVELOPMENT CONSIDERATIONS2.1 Clinical development plan

The broad aim of the process of clinical development of a new active substance is to f ind out

whether there is a dose ra nge a nd schedule a t w hich t he substa nce ca n be shown to be

simult a neously effective a nd sa fe, to the extent that the risk/benefit rela tionsh ip i s

a ccepta ble. The par ticular pat ients who benefit from the med icina l product, a nd the specif ic

indications for its use, also need to be defined.

Sa tisfying these broad aims usual ly requires a n ordered progra mme of cl inica l tr ials , ea ch

wit h its own specific objectives. This s hould be specified in a clinica l plan , or a series of

plans, with a ppropriat e decision points a nd f lexibi l i ty to a l low modif ica t ion a s kn owl edgea ccumula tes. An a pplica t ion for ma rketin g a uthorisat ion should clea rly describe the m a in

content of such plans, an d the contribution ma de by each tr ial . I nterpreta t ion a n d

a ssessment of the evidence from the total program me of tr ia ls involves synt hesis of the

evidence from the ind ividu a l tr ials (see Section 15). This is facilita ted by ensur ing that

common standards are adopted for a number of features of the tr ials such as dict ionaries of

medical t erms, def ini t ion a nd t iming of the ma in mea surement s, h a ndling of protocol

devia t ions and so on . A forma l s ta t i s t i ca l overview or meta -a na lys i s ma y be in form a t iv e

when medical questions are addressed in more than one trial . Where possible this should be

envisa ged in the plan so that the releva nt tr ia ls a re clearly identi f ied a nd a ny req uired

common features of their designs are speci f ied in advance.

Other ma jor sta t ist ical issues (i f a ny) w hich are expected to a f fect a number of tr ia ls in a

common plan should be addressed in that plan.

2.2 Confirmatory studies

As a rule , conf irma tory tr ia ls a re necessar y for the def ini t ive proof of ef f ica cy. In such

trials the key hypothesis of interest is always pre-defined, and corresponds to the hypothesis

which is subsequently tested when the tr ial is complete . However, in a conf irmatory tr ial i t

is equally important to estimate with due precision the size of the effects attributable to the

treatment of interest and to relate these ef fects to their cl inical signif icance.

Confirma tory tr ials a re the cornerst ones of decision ma king a nd hence a dherence to their

planned design and procedures is part icular ly importa nt ; una voida ble chan ges must be

explained a nd documented, an d their effect exam ined. A deta i led a nd just i f ied a ccount of


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the design of ea ch such tria l , an d of al l o ther sta t ist ical a spects such a s t he pla nn ed

analysis , should be set out in the protocol . Each tr ial should address only a l imited number

of questions.

Firm evidence of eff ica cy requires that the results of the pivota l conf irm a tory t r ia ls

demonstra te that the medical product under test has uneq uivoca l cl inical benef i ts . The

number of pivota l tr ia ls sh ould therefore be suf f icient to a nsw er each key cl inica l quest ion

releva nt to the ef f ica cy claim clea rly a nd def ini t ively. In add it ion i t is importa nt that the

basis for general isat ion to the intended patient populat ion is understood and explained; this

may also inf luence the number of pivotal tr ials required. Replicat ion of important studies is

of great value during the interpretation of results, especially when unforeseen problems have

arisen during conduct or analysis or when earl ier studies provide an insecure basis for the

ma in hypothesis to be tested.

2.3 Exploratory studies

The ra t iona le a nd des ign of conf i rma tory s tudies near ly a lwa ys rests on ear l ier c l in ica l

work ca rried out in a series of explora tory studies. Like al l cl inica l tr ia ls , t hese explora tory

studies should have clear and precise objectives. However, in contrast to conf irmatory

stud ies, th eir objectives ma y not a lw a ys lead to simple tests of pre-defined hy potheses. I n

a ddit ion, explorat ory st udies ma y sometimes require a more f lexible approach to design so

that changes can be ma de in response to a ccumula ting results . Their a na lysis ma y ent a i l

data exploration; tests of hypothesis may be carried out, but the choice of hypothesis may be

data dependent. Such studies cannot be the basis of the formal proof of efficacy, although they

may contribute to the total body of relevant evidence.

Any individual study ma y ha ve both conf irma tory a nd explora tory a spects . For exam ple, i nmost conf irmat ory studies the dat a a re also subjected to explora tory a na lyses wh ich serve a s

a basis for explaining or supporting their f indings and for suggesting further hypotheses for

la ter resea rch. The protocol should mak e a clear dist inction between the a spects of a study

which wil l be used for conf irmatory proof and the aspects which wil l provide data for

explora tory analys i s .

3. CLINICAL TRIAL DESIGNS

3.1 The parallel group design

The most common design of cl inical tr ial in Phase I I I is the paral lel group design in which

patients ar e ran domised to one of two or more arm s, ea ch a rm being a l located a di f feren t

treatment. These treatments wil l include the new medicat ion under investigat ion, at one or

more doses, a nd one or more control trea tm ents, such a s placebo a nd/or a n a ctiv e

compar a tor. In genera l t erms, the a na lysis of such tr ia ls a nd the interpreta t ion of their

results is straight-forward and is described in standard stat ist ical textbooks. However, even

in this relat ively simple si tuat ion biostat ist ical advice is st i l l necessary ( in accordance with

G CP ), because there ma y be a ddit iona l fea tures of the design w hich i t is importa nt or

essentia l to ta ke into account, but wh ich complica te the a na lysis a nd interpretat ion (e.g .

covariates, repeated measurements over t ime, interact ions between design factors) .


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3.2 The cross-over design

In the cross-over design of clinical trial , each patient is randomised to a sequence of two or

more trea tments, a nd hence a cts as h is/her own control for t reatm ent comparisons. Th is

simple manoeuvre is at tract ive primari ly because i t reduces the number of pat ients required

to a chieve a specific power, somet imes to a ma rked extent. In t he simplest 2x2 cross-over

design, each patient receives each of two treatments in randomised order in two successive

trea tm ent periods, often separa ted by a w a shout period. The most common extension of this

enta i ls comparing n(>2) trea tments in n periods, each patient receiving a l l n t reat ments.

Numerous variat ions exist such as designs in which each patient receives a subset of n(>2)

treatments, or ones in which treatments are repeated within a pat ient .

Cross-over designs have a number of problems w hich ca n inva l ida te their results . The ch ief

di f f icul ty concerns car ryover, that is the residua l inf luence of treat ments in subsequent

trea tment periods. In an a ddit ive model the ef fect of unequal car ryover wil l be to bias direct

treat ment compa risons. I n the 2x2 design the releva nt contr ast is t otal ly a l iased with the

interact ion between treatm ent and period and, w ha t is more, the test for either of these la cks

power because i t is a "betw een pat ient" contra st . This problem is less a cute in higher ord er

designs, but cannot be entirely dismissed.

When the cross-over design is used it is therefore important to avoid carryover. This is best

done by selective and careful use of the design on the basis of adequate knowledge of both the

disea se area a nd the new medica t ion. The disease under study should be chronic a nd sta ble.

The relevant effects of the medication should develop rapidly and be completely reversible.

The washout periods should be sufficiently long for residual effects to have disappeared. The

fact that these conditions are likely to be met should be established in advance of the trial by

means o f pr ior in format ion and data .

A common, and generally satisfactory, use of the 2x2 cross-over design is to demonstrate the

bioequivalence of two formulat ions of the same medicat ion in heal thy volunteers. Here, the

CP MP note for guida nce on I nvest i gat ion of B ioavai labi l i t y and Bi oequival encegives detai led

a dvice on how to plan, conduct a nd evalua te such tr ia ls . In this part icular a pplica t ion i n

heal th y volunteers, carr yover effects a re rat her unlikely to occur i f the wa sh-out t ime

between the tw o periods is sufficient ly long. How ever it is stil l importa nt to check th is

assumption during analysis on the basis of the data obtained, for example by demonstrat ing

tha t n o substa nce is detectable at the sta rt of each period.

There ar e a ddit iona l problems wh ich need car eful at tent ion in cross-over t ria ls. The m ost

notable of these are the complicat ions of analysis and interpretat ion arising from the loss of

patients , a nd t he di f f icul t ies of a ssignin g those a dverse events w hich occur in la ter

tr eat ment periods to the a ppropriat e tr eat ment. These, a nd other issues, a re described in the

guidelines on Dose Response I nform ati on to Support Produ ct Au th ori sati onprepared within

the Int erna tiona l Conference on Ha rmonisa t ion process. The cross-over design should

generally be restricted to situations where losses of patients from the trial are expected to be

s m a l l .

3.3 Factorial designs

In a f a c tor ia l des ign two or more t rea tments are evaluat ed s imul ta neously in the sa me

patient population through the use of varying combinations of the treatments. The simplestexa mple is the 2x2 factoria l d esign in wh ich pat ients are ra ndomly a l located to one of the

four possible combinations of two treatments, A and B say. These are: A alone; B alone; both


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A and B; neither A nor B. The usual intention of using this 2x2 design is to make efficient

use of cl inica l tr ia l pat ients by evalua ting the ef f ica cy of the two treat ments with the sa m e

num ber of pat ients a s would be req uired to evalua te the efficacy of either one alone. Th e

success of this approach depends upon the absence of any relevant interaction between

trea tments A a nd B so tha t th e ef fects of A a nd B on the primary ef f icacy varia bles fol low a na ddit ive model, an d hence the ef fect of A is virtua l ly identical w hether or not i t is a dd i t iona l

to the effect of B . As for the cross-over tr ia l , evidence that t his condit ion is likely to be met

should be establ ished in ad va nce of the tr ia l by means of prior informa tion a nd da ta . In

principle th is design ma y also be used for the specific purpose of exa min ing the int era ction

of A and B to look for non-additivity, but then the advantages of efficiency no longer apply

because much la rger tr ials a re necessa ry to detect cl inica l ly releva nt intera ct ion. The 2x2

design has proved to be part icularly valuable for very large mortal i ty studies.

Another important use of the factorial design is to establish the dose response characteristics

of a combination product e.g. one combining treatments C and D. A number, m, of doses of C

is selected, usua lly including a zero dose (placebo), and a sim ila r num ber, n, of doses of D.The ful l design then consists of mn treat ment groups, each receiving a di f feren t

combination of doses of C and D. The resulting estimate of the response surface may then be

used to help to identify an appropriate combination of doses of C and D for clinical use.

In the cl inical development of medicina l products there a re a number of other situa t ions

where these a nd other factoria l designs a re occas ional ly a ppropriat e . The detai led des ign

and analysis of these studies is a matter for professional stat ist ical at tention.

4. OTHER DESIGN ISSUES

4.1 Multicentre trials

A multicentr e tr ial is an a ccepted wa y of establ ishing the eff ica cy of a new medicat ion mor e

ef f iciently. Sometimes it provides the only mea ns of a ccruing suf f icient pat ients within a

reasona ble t ime-fra me. A further a dva nta ge commonly claimed for the mult icentr e tr ia l is

tha t it provides a better basis for subsequent genera l isa t ion of f indings, beca use the patients

a re recrui ted from a w ider popula t ion, a nd the medicat ion is ad ministered in a br oader

ra nge of cl inical set t ings, thus presenting a n experimental si tua t ion which is more typica l

of future use. In a ddit ion the involvement of a la rger number of investiga tors gives the

potential for more clinical judgement concerning the value of the medication.

The additional efficiency of the multicentre trial depends upon the assumption that thedif ferences betw een the compar ed treat ments are consta nt f rom centr e to centr e ; du ri ng

analysis, the robustness of the conclusions to this assumption generally needs to be explored.

I t is importa nt to design a nd conduct the tr ia l w i th this ba ckground in mind. P rocedures

should be sta nda rdised as completely as possible: va ria t ion of eva lua tion cri teria a n d

schemes can be reduced by investigator meetings, by the training of personnel in advance of

the study and by careful monitoring during the study. Good design should ensure a balanced

distribution of pat ients to trea tments wit hin each centr e and good ma na gement should

ensure tha t centr es do not diverge excessively in the num ber of pa tients entered. Fa ilure to

ta ke these preca utions, combined w ith doubts about the homogeneity of the results, ma y, i n

severe cases, reduce the va lue of a mult icent re tr ia l t o such a degree that it can not be

regarded as giving convincing evidence for the applicant 's claims.


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The a na lysis plan (see Section 10) for a multicentre t ria l should clea rly define t he centr es

(e.g. by investigator, location or region) in the context of the particular trial whenever there

is room for doubt . The pla n should also specify prospectively a ny int ention t o combine s m a ll

centres in the analysis, and the rules for so doing. The statistical model to be adopted for the

compa rison of tr eat ments should be described in t he protocol. The m odel sh ould g en er a llyallow for centre differences exceptions relate, for example, to large mortality studies with

very few pat ients per centre a nd simila rly the possibi li ty of qua l i ta t ive or quan ti ta t ive

centre by treatment intera ct ion should genera l ly be explored, as t his ma y af fect the

general isabi l i ty of the conclusions.

4.2 Trials to show superiority

Scienti f ica l ly, ef f ica cy is most convin cingly esta bl ished by demonstr a t ing superiority to

placebo in a placebo-cont rolled tria l . Simila rly , effica cy would norma lly be supported by

showing superiority to an active control treatment. This type of trial is later referred to as a

comparative trial (see Section 10.1.3).

4.3 Trials to show equivalence

When placebo-cont rolled tr ia ls ar e considered unet hica l, however, the demonst ra tion of

compar a ble ef f ica cy to that of a sta nda rd thera py (ra ther t ha n superiori ty) ma y a lso be

accepta ble provided a sui ta ble sta nda rd t herapy exists . [An example of a sui ta ble sta nda rd

thera py would be a w idely used therapy whose ef f ica cy in t he relevant indicat ion ha s been

clearly establ ished and quanti f ied in well designed and well documented placebo-control led

tria l(s).] This type of tr ia l is of ten cal led a n eq uiva lence tr ia l . In some ind ica t ions

equivalence tr ials a re also undert a ken for other regulat ory rea sons (see, for exam ple, notefor guida nce on Cl in ical Requi r ements for L ocally Appl ied, L ocally Actin g Produ cts, conta in in g

K nown Constitu ents). Eq uivalence tr ia ls ma y a lso incorporat e a placebo thus pursuing two

goals in one tr ia l i .e . esta bl ishing superiori ty to placebo a nd eva lua ting the degree of

similari ty to a reference treatment.

There are well known dangers associated with the use of the act ive control equivalence tr ial .

These relate to the implicit lack of any yardstick of internal validity (in contrast to placebo-

contr ol led tr ia ls), thus ma king externa l va l idat ion necessa ry. The equiva lence t r ia l is not

conservative in nature, so that most f laws in the design or conduct of the tr ial wi l l tend to

bias the results towa rds a conclusion of equiva lence. For these reasons a number of des ign

features need special at tention.

First a nd foremost , i t is vi tal tha t th e protocol of a tr ia l designed to demonst ra te equ iva lence

cont a ins a clear sta tement that this is i ts explici t intent ion. Secondly, the pr im a ry

measurement should be one which has been shown to be valid and reliable, and to reflect the

ma jor a spect of the disea se w hich the new t rea tment is in tend ed to improve. Thir dly , the

dose(s) selected for study, the patient population and other aspects of the design should be

such as to ensure adequa te sensi t ivi ty of the tr ial to detect relevan t di f ferences i f present .

Reassurance on this (and other issues) can of ten be gained by modell ing the study on earl ier

placebo-cont rolled st udies of the a ctive compar a tor in w hich the compa ra tor clea r ly

demonstr a ted cl inical ly va lua ble ef f icacy. F ina l ly, class ical hypothesis test ing (with the

null hypothesis that there is no difference between the treatments) is inappropriate, so that

sample size calculat ions need an al ternative basis (see Section 5) .


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There are also special issues in analysis . Pat ients who withdraw or drop out f rom treatment

can bias the results towards showing equivalence, and hence the intention to treat strategy

is insecure (see Section 10.1). Ana lys is is gener a lly ba sed a round the use of conf id en ce

int erva ls (see Section 10.4) a nd is directed a t esta blishing the la rgest possible trea tm ent

di f ference which might reasona bly be consistent with the observed results .

4.4 Dose Response designs

How response is relat ed to the dose of a new substa nce is a q uestion to wh ich a nswers ma y be

obtained in all phases of development, and by a variety of approaches. Dose response studies

ma y serve a number of objectives, amongst wh ich the fol lowing a re of part icular

importa nce: the confirm a tion of efficacy ; the invest iga tion of the sha pe a nd loca tion of the

dose response curve; the estim a tion of a n a ppropriat e sta rt ing dose; the ident if icat ion of

optima l stra tegies for individu a l dose a djustments; the determina tion of a ma xima l dose

beyond which a ddit iona l benefit w ould be un likely to occur. These objectives need to be

a ddressed using the da ta col lected at a number of doses under investiga t ion, perhaps

includ ing a placebo (zero dose). F or th is purpose the a pplica tion of estima tion procedures,

including the construction of conf idence intervals , and of graphical methods is as important

a s th e use of sta tist ica l tests. The hy pothesis tests w hich a re used m a y need to be ta ilored to

the special ordering of study arms or to the particular questions of interest in these studies:

does response increase monotonically with dose?; does response plateau or decline at higher

doses? The details of the planned statistical procedures should be laid down in the protocol.

4.5 Group sequential designs

The group sequent ia l design is the most common ly a pplied form of sequen tia l design. Th epurpose of a group sequ entia l design is to a llow the tr ia l t o be monitored a t specific t ime

interva ls so that a t reatm ent arm , or the entire tr ia l , ma y be stopped early i f there is clea r

evidence of efficacy or of una ccepta ble a dverse effects. Tria ls ma y a lso be stopped ea r ly

because the chance of ever showing a cl inica l ly valua ble benefi t is a ssessed a s too sm a ll .

However, the logist ics of a group sequentia l tr ial a re complica ted a nd r equire ca refu l

planning: an independent monitoring committee must general ly be employed: the stat ist ical

procedures must be fully specified in a dva nce (see Section 11.4) by th e monit oring comm itt ee

before they conduct their f i rst interim look a t t he dat a . This design is best reserved for la rg e

long-term trials of mortality or major non-fatal end-points.

5. THE SAMPLE SIZE

The number of pat ients in a cl inical tr ia l sh ould a lwa ys be lar ge enough to provide a

rel iable a nsw er to the questions a ddressed, but should a lso be the min imum necessa ry to

achieve this aim. This number is usually determined by the primary efficacy objective of the

tria l . I f the sa mple size is determined on some other basis , t hen this should be ma de clea r

and just i f ied. For example, a tr ial s ized on the basis of safety questions or requirements wil l

usually need larger numbers of patients. (See, for example, note for guidance on The Ext ent

of Popul ati on Exposur e to assess Cli ni cal Safety for M edi cin es in tend ed for L ong-t er m

Tr eatm ent of N on-l i fe-thr eateni ng Cond it ions.)The usua l meth od for determ inin g the a ppropriat e sa mple size r equir es s pecificat ion of a

primary va riable , the test sta t ist ic , the null hypothesis , the al terna tive ( w orking) hypothesis


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(embodyin g consid era tion of the trea tment differen ce to be detected or rejected), the

probability of erroneously rejecting the null hypothesis (the type I error), and the probability

of erroneously a ccepting t he null hypothesis (the type II err or), a s w ell a s t he a pproa ch to

dealing with dropouts and other protocol deviations. The method by which the sample size is

calculated should be given in the protocol, together with the estimates of any quantities usedin the calculat ions (such as va ria nces, mea n va lues, response ra tes, di f ference to be

detected). The basis of these estima tes should a lso be given; in confir ma t ory stu dies, they

should norma lly be ba sed on published da ta or on the results of ea rlier stud ies. Th e

treat ment di f ference to be detected ma y be based on a judgement concerning the m in im a l

effect which has cl inical relevance in the ma na gement of pat ients , or on a judgemen t

concerning the anticipated ef fect of the new treatment, where this is larger. Conventional ly

the type I error is set a t 5% or less; the precise choice of va lue is influen ced by the prior

plau sibility of the hypothesis under test an d the desired impa ct of the results. The t ype II

error is conventiona l ly set at 20% or less; i t is in the investiga tor's interest to keep this

figure as low as possible especially in the case of studies which are diff icult or impossible to

repeat.

When the va ria nce of the prima ry va ria ble , or the contr ol response rat e , is pa rt icula rly

uncerta in, i t ma y be worth wh ile to carr y out a su i ta bly bl inded int erim est ima tion of the

qua nti ty in question in order to updat e the sam ple size appropriately. Any such plans should

be ca refully described in the protocol the steps ta ken to preserve blind ness should be

explained, together with the conseq uences (if a ny) for the type I error a nd the widt h of

confidence intervals. (See also Section 11.3).

Sa mple size calculat ions sh ould make appropriat e a l low a nce for dropouts and a ny other

anticipated protocol deviations which may affect power. Not only should the sample size be

increased to offset the loss of patients from the study or from their intended treatments, but italso should allow for the fact that the size of effect observed may be reduced by the need to

include any a vai l able dat a from t reatment f a i lures or other ear ly te rminat ors in a n

intent ion-to-tr eat a na lysis (see S ection 10.1.1).

The sa mple size of a n equ iva lence t ria l (see Section 4.3) should norma lly be ba sed on the

objective of obtaining a confidence interval for the treatment difference which is sufficiently

na rrow to exclude a non-negligible di f ference, given that the trea tments ar e t ruly

equivalent . The choice of non-negligible di f ference r equires just i f ica t ion, a nd ma y be

sma ller tha n the minim a l cl inical ly releva nt di f ference referred to above in the context of

tr ia ls designed to esta bl ish t ha t a di f ference exists . In bioequivalence t r ials the use of a 90%

confidence int erva l is conventiona l ; t herapeutic cl inical tr ia ls ma y r equire the use of

confiden ce in ter va ls w ith great er covera ge proba bility (e.g. 95%) in order to a chiev e

suf f icient impact .

The sa mple size in a group sequentia l t r ia l cann ot be f ixed in a dva nce beca use i t depends

upon the play of chance in combination with the chosen stopping rule and the true treatment

difference. The design of the stopping rule should ta ke into a ccount the conseq uent

distribution of the sa mple size , usual ly embodied in the expected a nd ma ximum sa mple

s izes .

6. THE POPULATIONIn the ea rlier pha ses of product development the choice of pat ients for a clinica l tr ia l ma y be

hea vily influenced by the w ish to ma ximise th e cha nce of observing specific clinica l effects


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of interest , and h ence they ma y come from a very na rr ow sub-group of the tota l pa tient

populat ion for which the substa nce may eventua l ly be indica ted. However by the t ime the

pivota l Pha se I I I tr ia ls a re underta ken, the patient popula t ions should more closely m ir r or

the intended users. Hence in these tr ia ls i t is genera l ly helpful to relax the inclusion a n d

exclusion as much a s possible wit hin the ta rget indicat ion, whilst ma int a inin g suf f icienthomogeneity to permit a successful trial to be carried out. No individual clinical trial can be

expected to be tota lly representa tive of fut ure users, beca use of the possible influ ences of the

geographical location, the time when it is conducted, the medical practices of the particular

invest iga tor(s) and clinics , a nd so on. How ever the influen ce of such factors sh ould be

reduced wherever possible , a nd subsequently discussed during the interpreta t ion of the t r ia l

resul ts .

I t is unusua l for a l l el igible pat ients considered for entry to a tr ia l to be included. In pivota l

tr ia ls, i t is recomm ended that a log should be kept of all screened pat ients so a s to a llow

some assessment of the numbers a nd char a cterist ics of the excluded patients , a nd the

reasons for their exclusion.

7. DESIGN TECHNIQUES TO AVOID BIAS

The tw o most importa nt design techniques for a voiding bias in cl inica l tr ia ls a re bl in di ng

a nd randomisat ion, a nd these should be a norma l featur e of most contr olled cl inical t r ia ls

intended to be included in the regulatory applicat ion for a new product . Most such tr ials

follow a double-blind approach in which treatments are pre-packed in accordance with a

sui table ra ndomisa tion schedule, and supplied to the tr ia l centr e(s) la bel led only with the

patient number and the treatment period so that no-one involved in the conduct of the trial is

aware of the speci f ic treatment al located to any part icular pat ient , not even as a code let ter .

This approach will be assumed in Sections 7.1 and most of Section 7.2, exceptions being

considered a t the end.

7.1 Blinding

B lind ing is int ended to limit the occurren ce of conscious a nd u nconscious bias in the

conduct a nd interpreta t ion of a cl inica l tr ia l arising from the inf luence wh ich the

knowledge of treat ment ma y ha ve on the recrui tment a nd a l locat ion of pa t ients , their

subsequent care, the attitudes of patients to the treatments, the assessment of end points, the

ha ndling of withdra wa ls, the exclusion of dat a f rom ana lysis , a nd so on. The essentia l a i mis to prevent identif ication of the treatments until all such opportunities for bias are passed.

In a double-bl ind t r ial nei ther the patient nor a ny of the sta f f involved in the treatment or

cl inical evaluation of the patient is aware of the treatment received. In a single bl ind tr ial

the investiga tor a nd/or his sta f f ar e aw a re of the treat ment but not the patient . In a n open-

la bel tr ia l the identity of tr eat ment is kn own to a ll . The double-blind t ria l is t he optima l

approach. This requires that the treatments to be applied during the trial cannot be

dist inguished in any way (appearance, taste , e tc .) e i ther before or during administrat ion.

Dif f icul t ies in a chieving the double-bl ind ideal ca n a rise : the treat ments may be of a

completely di fferent na tur e for exa mple, sur gery a nd medicina l product therapy; two

substa nces may ha ve di f ferent ga lenic forms a nd, a l though they could be ma deindist inguisha ble by the use of ca psules, chan ging the ga lenic form might a lso cha nge the

phar ma cokinetic and/or phar ma codyna mic propert ies and hence require th a t bioequivalence


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of the forms be establ ished; the dai ly pattern of administrat ion of two treatments may di f fer .

One way of achieving double-blind conditions under these circumstances is to use a double

dummy technique. This technique may sometimes force an administrat ion scheme which is

suf f iciently unusua l to inf luence a dversely the motiva t ion a nd compliance of the patients .

Et hica l di f f icul t ies ma y a lso int erfere with its use when, for example, it ent a i ls du m m yoperative procedures. Nevertheless extensive efforts must be made to overcome these

di f f i cu l t ies .

If a double-blind trial is not feasible, then the single blind option should be considered. In

some cases only an open-label trial is practically or ethically possible. Under either of these

circumst a nces i t is prefera ble, where possible , for cl inica l a ssessments to be ma de by

medical sta f f who a re not involved in tr eat ing the patients a nd wh o rema in bl ind to

trea tm ent. In single blind or open-la bel tr ia ls every effort should be ma de to min imis e the

various known sources of bias. The reasons for the degree of blinding adopted should be

explained in the protocol, together with steps taken to minimise bias by other means.

Any intent iona l or unintent iona l brea king of the bl ind must be reported at the end of the

trial , irrespective of the reason for its occurrence.

7.2 Randomisation

Randomisation introduces a del iberate element of chance into the assignment of treatments

to patients in a cl inical tr ial . D uring subsequent an a lysis of the tr ia l da ta , it provides a

sound sta t ist ical ba sis for the qua nti t a t ive evalua tion of the evidence relat ing to treat ment

effects. I t also tends to produce treatment groups in which the distributions of prognostic

f ac tors (known a nd unknown ) are s imi lar . In combinat ion wi th b l inding , ra ndomis a t ion

helps to a void possible bia s in the selection a nd a lloca tion of pa tients a risin g from thepredictabi l i ty of treatment assignments.

The ra ndomisa tion schedule of a cl inical tr ia l documents the ra ndom a l locat ion of

treat ments to patients . In the simplest si tua t ion i t is a sequential l is t of t reat ments (or

treatment sequences in a cross-over study) or corresponding codes by patient number. The

logist ics of some studies, such a s those with a s creening phase, ma y ma ke ma tt ers more

complicated, but the unique pre-planned a ssignm ent of treatment, or trea tment sequence, to

pat ient should be clea r. Different d esigns of study w ill r equir e different procedures for

genera tin g r a ndomisa tion schedules. This procedure should be capa ble of being reproduced

(if the need arises) through the use of the same random number table, or the same computer

routine and seed for i ts random number generator.

Although unrestricted ra ndomisa tion is an a ccepta ble a pproach, some adva nta ges ca n

genera l ly be ga ined by ra ndomis ing patients in blocks. This helps to increase the

comparabi l i ty of the treatment groups part icularly when patient characterist ics may change

over time, as a result, for example, of changes in recruitment policy. I t also provides a better

guar a ntee that the trea tment groups wil l be of nea rly equa l size . I n cross-over tr ials i t

provides the mea ns of obta ining ba lan ced designs with their greater ef f iciency a nd ea sier

interpretation. Care must be taken to choose block lengths which are sufficiently short to

l imit possible imbalance, but which are long enough to avoid predictabi l i ty towards the end

of the sequence in a block. Investigators should generally be blind to the block length; the use

of tw o or more block lengt hs, r a nd omly selected for each block, can a chieve the sa m e

purpose. (St rictly, in a double-blind tr ial predicta bility does not ma tt er, but the

pharmacological effects of medicinal products often provide the opportunity for intelligent

g u e ssw o rk . )


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In mult icentr e studies the ra ndomisa tion procedures should alw a ys be organ ised cent ra l ly.

I t is a dvisa ble to ha ve a separa te ra ndom scheme for each centr e i .e . to stra t i fy by centre .

More genera l ly, s tr a t i f icat ion by importa nt prognostic factors measured a t basel ine (e .g .

severity of diseas e, age, sex, etc.) ma y sometimes be va lua ble in order to promote ba la nced

al locat ion within strata; this has greater potential benef i t in small tr ials . The use of moretha n two or three str a t i f icat ion factors is ra rely necessary , is less successful a t a chiev in g

balance and is logist ical ly troublesome. Where i t i snecessary the use of a dy na mi c

a lloca tion pr ocedure (see below) ma y help to a chieve ba la nce a cross a ll f a ctors

simultan eously provided the rest of the tr ia l procedures can be a djusted to a ccommoda te a n

a pproa ch of this t ype.

The next pat ient to be randomised into a study should always receive the treatment

corr esponding to the next free number in the a ppropriat e ra nd omisa tion schedule (in the

respective stra tum, if ra ndomisa t ion is stra t i f ied). The appropriat e number a nd a ssocia ted

trea tment pack for the next pat ient should only be a l located when entry of that pat ient to the

ra ndomised pa rt of the tr ia l ha s been conf irm ed. These ta sks wil l norma lly be carr ied outby sta f f at the investiga tors centre , who wil l then dispense the releva nt bl inded t r ia l

supplies. Detai ls of the ra ndomisa tion w hich faci li ta te predicta bi l ity (e .g . block lengt h)

should not be cont a ined in the ma in stud y protocol, but should be set out in a n a dd end um

which can be withheld from the study sites. The randomisation schedule itself should be

f i led securely by the a pplica nt in a ma nner wh ich ensures that bl indness is properly

maintained throughout the tr ial . Access to the randomisation schedule during the tr ial must

ta ke into account the possibil i ty tha t , in a n emergency, the bl ind ma y ha ve to be broken for

a ny pa tient, either par tia lly or completely. The procedur e to be followed, the ne cess a ry

documentat ion, and the subsequent treatment and assessment of the patient should al l be

described in the protocol.

Alterna tive ra ndomisa tion procedures genera l ly require some relaxa tion of the degree of

bl indness. An important case is when the treatment codeof each patient is known al though

the assignment of actua l trea tment to treat ment codes is n ot ; this is st i l l t echnical ly double-

bl ind but the groups of pat ients on a common trea tment a re identi f iable . This relaxa tion i s

necessa ry to permit the norm a l methods of dy na mic a lloca tion to be used. In t hese, the

a l locat ion of treat ment to a pat ient ma y be inf luenced by the current bala nce of a l loca ted

treatments and, in a strat i f ied tr ial , by the stratum to which the patient belongs and the

balance within each prognostic factor. Knowledge of the treatment code may be restricted to a

centr a l tr ia l off ice from w here the dyn a mic a l locat ion is cont rol led, genera l ly through

telephone conta ct . This in turn permits ad dit iona l checks of el igibi l i ty cri teria a n d

establ ishes entr y into the tr ial these fea tures can be va luable in certa in types of mult icentretrial . The usual system of pre-packing and labelling product supplies for double-blind trials

can then be followed, but the order of their use is no longer sequential . (It is even possible

thr ough the use of a ppropriat e computer a lgorith ms to keep the personnel at t he centra l t ri a l

office blind to the treatment code.)

Single bl ind a nd open-label tr ia ls provide ad dit iona l f lexibi l ity , but in t hese i t i s

par t icular ly importa nt to ta ke care that the investiga tors knowledge of the next t reat ment

does not influen ce his decision to enter the pat ient a s ra ndomis ed: his decision should

always precede knowledge of the randomised treatment. Any decision to reduce the level of

bl inding in order to use a part icular method of randomisation requires careful just i f icat ion.


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8. PRIMARY AND SECONDARY VARIABLES

The primary variable ( target variable , primary endpoint) should be the variable capable of

providing the most releva nt a nd convin cing evidence directly related to the pr im a ry

objective of the tr ia l . There should genera l ly be only one prima ry va ria ble a nd this w il lusua l ly be a n ef f ica cy cri terion, beca use the prima ry objective of most conf irm a tory t r ia ls

concerns efficacy. The selection of the prima ry va ria ble must reflect th e a ccepted norms a n d

standards in the relevant f ie ld of research. The use of a rel iable and val idated variable with

wh ich experience has been gained either in ear l ier studies or in published l i terat ure i s

recommend ed. There should be sufficient evidence that the prima ry va ria ble w ill be

sensit ive to clinica lly releva nt t reat ment effects in the pat ient populat ion described by the

inclusion and exclusion cri teria .

The primary variable should be specified in the protocol. A post-hoc definition will rarely be

a ccepta ble, since the biases th is int roduces are diff icult to a ssess. When the clinica l effect

defined by the primary objective is to be measured in more than one way, then the protocol

should identi fy one of the measurements as the primary variable , whenever possible . I f this

is not possible, a nother useful stra tegy is to combine the mult iple mea surem ents into a

single va ria ble , perha ps with sui table weight ing; indeed, the prima ry va ria ble somet imes

a rises na tur a l ly a s a combina tion of mult iple clinica l mea surements (e .g . the ra t ing sca les

used in a rth ri t is , psychiat ric disorders a nd elsew here). I n ei ther ca se, the method of

combinin g the mult iple mea surem ents should be specified in the protocol, an d a n

interpretation of the new scale should be provided in terms of the size of a clinically relevant

benefit . The primary variable is also the most appropriate one to use in the protocol for

estimating the sample size (see section 5).

I t may sometimes be desirable to use more than one primary variable to cover the range of

effects of the therapies, simultaneous evidence of effect on each of them (or a pre specified

subset of th em) being sought in order to demonstra te effica cy of the product. The pla nn ed

ma nner of interpret a tion of this type of evidence must be ca refully spelled out a nd the effect

on the type I error explained, because of the potential for multiple comparison problems (see

Section 10.5).

When direct measu rement of the clinica l benefit to the pat ient is not feas ible, in dir ect

cri teria (so-cal led surr oga te va ria bles) ma y ha ve to be considered. The use of a surr ogat e

va ria ble a s a prima ry va ria ble requires ca reful just i f ica t ion of the claim that , under the

circumsta nces of the tr ia l , the a nticipat ed or observed trea tment effects on the surr ogat e

variable predict clinical benefits of value to the patient.

Secondary variables are ei ther supportive measurements related to the primary objective or

mea sur ement s of effects rela ted to the seconda ry objectives. Their pre-definition in the

protocol is also important.

On some occa sions cat egorisa t ion or dichotomisa t ion of continuous or ordina l va ria bles

may be necessary in which case the criteria should be specified in advance in the protocol.

Criteria of success and response are common examples of dichotomies which require precise

specif ica t ion in terms of , for exa mple, a minim um percenta ge improvement (relat ive to

ba sel ine) in a continuous var iable , or a ra nking ca tegorised as a min imum of good on a n

ordinal ra t ing sca le .


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9. THE CASE REPORT FORM

The form and the content of the case report forms (CRFs) must be in full accordance with the

protocol a nd must be esta blished in a dva nce of the conduct of the study . Ca se report f or m s

should only include releva nt i tems w hich wil l be evaluat ed in t he f ina l report . Da ta f ie l dsshould be designed so that mis sing va lues can be dist inguished from va lue zero or

characterist ic absent . Verbal scales should be exhaustive and overlapping categories

should be a voided so that una mbiguous a nsw ers a re obta ined. I t is genera l ly mor e

appropriate to document the absolute value on a ra t ing scale ra ther tha n changes from a

basel ine. I f changes a r edocument ed, then the time point to wh ich the chan ge is rela ted

should be made clear and unambiguous.

The CRF should be fil led out during the course of the trial and the dates to which the data

apply and on which the form was completed should be noted. Subsequent additions or

a mendments to th e form should be avoided, except a s a means of correcting errors ident i f ied

before analysis during a planned process of monitoring or qual i ty control , in which case the

changes should be properly documented, signed and dated.

Simila r considera t ions a pply to dat a col lected via a medium other tha n paper, such a s the

electronic medium employed in remote data entry. Further guidance relat ing to CRFs can be

found in Cha pter 3 of G CP .

10. PRE SPECIFIED DATA ANALYSIS

When designing a clinical t r ia l , i t is good practice to consider the eventua l a na lysis of the

data and to document the result ing plans the analysis plan . In the case of an exploratory

tria l the plan ma y describe only genera l principles a nd directions, but in a conf irm a t ory

tr ial th e plan should be precise in a number of respects if the credibility of the find ing s is to

be maximised. All features of the proposed conf irmatory analysis of the primary variable(s) ,

including the wa y in which ant icipated an a lysis problems wil l be ha ndled, should be

covered in the plan n orma lly w ith in the protocol. The principal feat ures of the a na lys is of

a l l other da ta should a lso be outl ined.

I t is a lso valua ble to review the a na lysis plan w hen the study dat a a re complete a n d

avai lable for review but whilst the stat ist ician (amongst others) is st i l l bl inded to treatment,

and hence before the main analysis . This wil l be referred to as the bl ind review.

10.1 Study populations

The analysis plan should f irst def ine the populat ion of pat ients whose data i t is planned to

include in the main ana lyses . In addi t ion in p ivota l t r i a l s any a vai l a ble da ta on the w ider

population screened for entry, or enrolled into a screening phase of the study prior to

ra ndomisa tion, should be summ a rised wit hin the bounds (i f a ny) imposed by the need for

informed consent . The intention of this plan ned summ a ry is to provide informa tion about

the num bers a nd cha ra cterist ics of excluded pat ients, both eligible a nd ineligible, together

with their reasons for exclusion, in order to guide a ssessment of the potentia l pra ct ica l

impact of the study results . As a min imum , documenta t ion is required for a l l pat ients for

whom study procedures were ini t iat ed a nd w ho ha ve given their informed consent . The

content of this patient documentation depends on detailed features of the particular trial , but

at least demographic a nd ba sel ine dat a on disease stat us should be col lected w henever

possible.


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I f al l pat ients randomised into a cl inical tr ial sat isf ied al l entry cri teria , fo l lowed al l tr ial

procedures perfectly w ith n o losses to follow u p, and provided complete da ta records , then the

populat ion of pa tients to be included in the a na lys is w ould be self-evident. The design a n d

conduct of a trial should aim to approach this ideal as closely as possible but, in practice, i t is

doubtful i f it can ever be ful ly a chieved, an d hence the a na lysis plan should a ddress a n yanticipated problems prospectively in terms of how these affect the patients and data to be

a na lysed. Decisions concerning the a na lysis popula t ion should be guided by the prin ciples

underlying the intention-to-treat and the per protocol strategies.

10.1 .1 Th e in ten t i on -t o -t r ea t popu la t i on

The principle of intention-to-treat (ITT) implies that all randomised patients should be

included in the a na lysis . In most cl inical tr ials i t provides a conserva tive a pproach, a n d

a lso gives estima tes of tr eat ment effects w hich are more likely to mir ror those observed i n

subsequent pra ctice. In practice the protocol should t ry t o a void or a meliora te each type of

i r regula r i ty which i s an t ic ipated dur ing the t r i a l a nd w hich might impai r a sa t i s f a c tory

ITT an a lysis . Wherever possible, it should also def ine prospectively how a ny un a voida ble

problems wil l be a ddressed. Any objective entry cri teria , measur ed before ra nd omisa t ion,

which will be used to exclude patients from analysis should be pre-specified and justif ied, for

exam ple, those rela tin g to the presence or a bsence of the disea se und er invest iga tion. An y

other anticipated reasons for excluding patients from ITT analysis should be justif ied.

The problems a ssociat ed with ITT l ie in the ha ndling of some irregula ri t ies (incorr ectly

entered pat ients , errors in treat ment assignment, missin g da ta , loss to fol low up, a nd some

other protocol violat ions) an d the subtleties wh ich t his ca n involve. For exam ple, pat ients

who fai l to sa t isfy a n objective entr y cri terion measur ed prior to ra ndomisa tion, but who

erroneously enter the tr ial , may be excluded from analysis without introducing bias into thetreat ment compa rison. H owever not a l l incorrectly entered patients fa l l into this cat egory.

As another example, pat ients withdrawn from treatment may introduce serious bias and, i f

they have provided no data af ter withdrawal , ITT of fers no obvious solution. The necessary

inclusion of such patients in the a na lysis ma y require some re-def ini t ion of the pr im a ry

var iable , or some assumptions a bout the pa tients fat e .

Measur ements of prima ry va ria bles ma de at the t ime of wit hdra wa l (or a t the t ime of the

loss of the pat ient for a ny other reas on), or subsequent ly collected in a ccord a nce wit h the

protocol, a re va lua ble in t he context of ITT a na lysis . Their use in a na lys is should be

described and just i f ied in the a na lysis plan a nd their collect ion described elsewh ere in the

protocol . However, the use of techniques such a s last observat ion carr ied forwa rd (LOC F)should recognise the fact that it ca n lea d to biased est imat es of t reat ment ef fects when the

likelihood of the loss of a pa tient is rela ted to trea tm ent or r esponse. Any other methods to be

employed to ensure the a va i labi l i ty of measu rements of the prima ry va ria ble for ev ery

patient in the ITT analysis should be described.

Because of the complexity of the problems connected with ITT it may sometimes be preferable

to defer deta i led considera t ion of the ma nner of dea l ing with irregula ri t ies unti l the bl in d

review of the data at the end of the study a nd, i f so, this should be stat ed in the ana lysis plan.


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10.1 .2 Th e per pr o toco l popu la t i on

The per protocol populat ion, sometim es described a s the va lid cas es, the eff ica cy

populat ion or th e evalua ble pa tient populat ion, is a subset of the intention-to-tr eat populat ion

and is characterised by the fol lowing cri teria :

the completion of a certain pre-specified minimal exposure to the treatment regimen,

the a vai l a bi li ty of measurements of the pr imary var iable(s) a t re levan t a nd

pre-specified time(s),

the a bsence of a ny ma jor protocol violat ion including the viola t ion of entry cri t eria

(w here the na tu re of and rea sons for these protocol violat ions must be defined a n d

documented before breaking the blind).

This populat ion general ly maximises the opportunity for a new treatment to show addit ional

efficacy in a na lysis , an d m ost closely r eflects the scient if ic model un derly ing the protocol.

However it is not conservative, and is more vulnerable to biases than ITT.

10.1 .3 Th e r o l es o f the i n ten t i on - t o -t r ea t an d t h e per pr o toco l an a l yses

In general , i t is adva nta geous to demonstra te a lack of sensi t ivi ty of the principa l t r ia l

results to al ternative choices of pat ient populat ion for analysis . In pivotal tr ials i t is usual ly

a ppropriat e to plan to conduct both ITT a nd per protocol an a lyses , so that an y di ffer ences

between them can be the subject of explicit discuss ion a nd interpret a tion subsequ ently. I n

some cases, i t may be desirable to plan further exploration of the sensitivity of conclusions to

the choice of populat ion an a lysed . When the ITT an d the per protocol an a lyses come to

essentia l ly the sa me conclusions, conf idence in the study results is increa sed, bear ing i n

mind, however, that the need to exclude a substantialproport ion of the ITT populat ion f r om

the per protocol analysis throws some doubt on the overall validity of the study.

ITT and per-protocol analyses play different roles in comparative trials (which seek to show

one active substance to be superior), and in equivalence trials (which seek to show

medicina l products to be similar see Section 4.3). In compar a tive stu dies the ITT a n a ly si s

usua l ly tends to a void the optimist ic est imate of ef f ica cy wh ich m a y result f rom a per

protocol a na lysis , s ince the noncompliers included in a n ITT a na lysis w il l gen er a l ly

diminish the overa l l t reat ment ef fect . However in a n equiva lence tr ial I TT no long er

provides a conservat ive stra tegy and i ts role should be considered very careful ly. Hence i n

compar a tive tr ials , part icularly t hose cla iming to be pivota l w ith rega rd to ef f icacy, the I TT

a na lysis w il l norma lly be of higher priori ty, wherea s in equiva lence t r ia ls this is not the

case .

10.2 Missing values and outliers.

Missing values represent a potentia l source of bias in a cl inica l tr ia l . H ence, every ef fort

should be undert a ken to fulfil a ll the requ irement s of the protocol concernin g the collection

of data a nd the ir subsequent ma na gement . However , in rea l i ty there wi l l a lmost a lwa ys be

some missing data. A study may be regarded as valid, none-the-less, provided the methods of

deal ing with missing values are sensible , and part icularly i f those methods are pre-def ined

in the a na lysis pla n of the protocol. P re-def ini t ion of methods ma y be faci l ita ted by upda ting

th is aspect of the a na lys i s p lan dur ing the b l ind review. Unfor tunat e ly , no un iver sa l lya pplica ble methods of ha ndling missin g va lues can be recommended. An in vest iga t ion


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should be ma de concernin g the sensit ivity of the results of a na lys is to the method of

handling missing values, especial ly i f the number of missing values is substantial .

A sim ila r a pproa ch should be a dopted to explorin g the influen ce of outliers, the st a tis tica l

def ini t ion of wh ich is , to some extent , ar bi tra ry. Clear identi f ica t ion of a part icular value a s

a n outl ier is most convin cing wh en just i f ied medical ly a s well as sta t ist ica l ly, and the

medical cont ext will th en often define the a ppropria te a ction. Any outlier procedure set out i n

the protocol should be such as not to favour any treatment group a p r io r i . Once a ga in, t his

aspect of the analysis plan can be useful ly updated during bl ind review. I f no procedure for

deal ing with outl iers wa s foreseen in the study protocol , one a na lysis with the a ctual va lues

an d at least one other a na lysis el imina tin g or reducing the outl ier effect should be

performed and differences between their results discussed.

10.3 Data transformation/modification

The decision to transform key variables prior to analysis is best made during the design ofthe tr ia l on the basis of simila r dat a from ear l ier cl inica l tr ials . Tra nsform a tions (e.g .

square root, logarithm) should be specified in the protocol and a rationale provided,

especia lly for the prim a ry va ria ble(s). The genera l principles gu iding the use of

transformations are to be found in standard texts ; conventions for part icular variables have

been developed in a num ber of specific clinica l a rea s. The decision on whether a nd how to

tr a nsform a va ria ble should be inf luenced by the preference for a scale wh ich fa ci l i ta tes

c l in ica l in terpre ta t ion .

Simila r considera t ions apply to other dat a modif ica t ions sometimes used to creat e a k ey

va ria ble for a na lysis , such a s the use of change from basel ine, percenta ge change fr om

baseline, the area under the curve of repeated measures, or the ratio of two differentva ria bles. Subsequent cl inical interpreta t ion should be careful ly considered, a nd the

modification should be justif ied in the protocol. Closely related points are made in Section 8.

10.4 Estimation, confidence intervals and hypothesis testing.

The st a tist ical a na lysis pla n should specify the hypotheses which a re to be tested a nd/or the

treatment effects which are to be estimated in order to satisfy the objectives of the trial . The

sta tist ical methods to be used to a ccomplish these ta sks sh ould be described for the pr im a r y

(a nd preferably the secondar y) va ria bles, a nd the under lying sta t ist ical model should be

ma de clear . E st ima tes of treatment effects should be a ccompanied by conf idence int erva ls ,

wh enever possible, a nd the w a y in w hich these w ill be calcula ted should be ident if ied. Theplan should also describe any intentions to use basel ine data to improve precision and to

adjust est ima tes for potentia l ba sel ine di f ferences, for exam ple by mea ns of a na lysis of

cova ria nce. The report ing of precise numer ica l probabilities (e.g.P= 0.034) should be

envisaged in the plan, rather than exclusive reference to critical values (e.g. P


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covariates f i t ted in an analysis of covariance. (See also Section 10.6) . Due at tention should

be paid to the sta t ist ical distr ibution of both primar y a nd secondar y va ria bles. The pre-

planned use of non-parametric methods to avoid distribution diff iculties is acceptable. When

ma king this choice i t is importa nt t o bea r in mind t he need to provide stat ist ical est imat es of

the size of trea tment ef fects , together with conf idence interva ls , a s t his ma y inf luence thechoice of method in ca ses of doubt. Any essent ia l cha nges to the pre-plan ned st a tist ical

modelling procedure should be made during blind review.

The a na lysis of the prima ry va ria ble by which the prima ry objective of the tr ial w i l l be

judged must be clearly dist inguished from supporting analyses of the primary or secondary

va ria bles. In these other a na lyses, the number of signif ican ce tests should be m in im is ed

a nd preference given to descriptive methods a nd estima tion procedures w henever possible.

Within the analysis plan there should also be an outl ine of the way in which data other than

the primary and secondary variables wil l be summarised and reported. This should include

a r eference to a ny approa ches adopted for the purpose of a chieving consist ency of a na ly si s

across a range of studies, for example for safety data.

10.5 Adjustment of type I error

When multipl icity is present , the usual frequentist a pproach to the a na lysis of cl inica l t r ia l

dat a may require an a djustm ent to the type I error. Mult iplici ty ma y a rise f rom mult iple

primary variables (see Section 8) , mult iple comparisons of treatments, repeated evaluation

over t ime an d/or interim a na lyses (see Section 11.4). Methods t o avoid or r educe mu lt iplicit y

a re sometimes preferable wh en a va i lable , such as the identi f icat ion of the key p ri ma ry

va ria ble (mult iple varia bles), the choice of a cri t ica l trea tment contra st (mult iple

compa risons), the use of a summ a ry measur e such as a rea under the curve (repeated

meas ures), an d the use of extreme type I errors (interim a na lysis) . In conf ir ma t ory

analyses, any aspects of mult ipl ici ty which remain af ter steps of this kind have been taken

should be identi f ied in the protocol ; adjustment should a lwa ys be considered a nd the deta i ls

of a ny a djustment procedure should be set out in the a na lysis pla n.

10.6 Subgroups, interactions and covariates

The prima ry va ria ble(s) is of ten syst ema tica l ly related to other inf luences apa rt f r om

treat ment. For example, there ma y be relat ionships to cova riat es such a s a ge a nd sex, or

there may be differences between specific subgroups of patients such as those treated at the

dif ferent centres of a mult icentre tr ial . In some instances an adjustment for the inf luence of

covariates or for subgroup ef fects is an integral part of the analysis plan and hence should

be set out in the protocol. Pre-study deliberations should identify those covariates and factors

expected to ha ve a n importa nt in f luence on the prima ry va ria ble(s), a nd should consi der

how to account for these in the analysis in order to improve precision and to compensate for

any lack of balance between treatment groups. When the potential value of an adjustment is

in doubt , i t is of ten a dvisa ble to nomina te the una djusted ana lysis a s the one for pr im a ry

at tention, the a djusted a na lysis being supportive. Special a t t ention should be pa id to centr e

ef fects and to the role of basel ine measurements of the primary variable . I t is not advisable

to adjus t the main analyses for covar ia tes measured a f ter randomisat ion .

The treatment effect itself may also vary with subgroup or covariate for example, the effect

ma y decrease with a ge or ma y be lar ger in a par t icular dia gnostic cat egory of pat ient . I n

some cases such interact ions are anticipated, and hence a subgroup analysis , or a stat ist ical

model includin g intera ct ions, is part of the conf irma tory a na lysis plan. In most cas es,


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however, subgroup or intera ct ion a na lyses a re exploratory a nd should be clea rly iden ti f ied

as such; they should explore the uniformity of a ny trea tment ef fects found overal l . I n

general , such analyses should proceed through the addit ion of interact ion terms to the

stat ist ical model in question, rather than through mult iple separate analyses within each

subgroup of pat ients , or w ithin stra ta def ined by the cova ria tes. When explora tory, thesea na lyses should be carr ied out informa lly a nd interpreted cautiously; an y cla ims of

trea tment ef fica cy ba sed solely on explora tory subgroup a na lyses ar e unlikely t o be accepted.

11. THE CONDUCT AND MONITORING PHASE

Careful conduct of a trial according to the protocol has a major impact on the credibility of

the study results . Careful monitoring can ensure that di f f icul t ies are noticed early and their

recurrence minimised . Both he lp to permi t a s t r a igh t forwa rd an d una mbiguous a na ly s i s .

The period of conduct a nd m onitor ing sta rts with the selection of the stud y sites a nd en ds

wit h the collection a nd clea nin g of the la st pat ients da ta . In some ca ses, employees of the

sponsor may suf f ice to monitor the qua l i ty of the tr ia l a ct ivit ies a nd da ta , while in other

cases a n independent a nd experienced body of special ists (a monitoring committ ee) w il l

a lso be required. The lat ter is appropriate i f forma l interim a na lyses a re plann ed, with

some lif ting of th e blindness being necessar y, an d/or if regula r a nd independent reviews of

safety are required. The employees of the sponsor and the monitoring committee both require

access to sta t ist ical expert ise for advice a nd a ssista nce. This ma y relate to the ha ndling of

unexpected protocol violat ions to min imis e effects on the an a lys is (sponsor), or to the

execution, interpretat ion or modif icat ion of interim analyses (monitoring committee) .

11.1 Changes in inclusion and exclusion criteria

Inclusion and exclusion criteria should, if possible, remain constant, as specified in the

protocol, throughout the period of pat ient recruit ment . H owever, occa siona lly this ma y not

prove possible; in long-term stu dies, for exam ple, grow ing medica l k now ledge either fr om

outside the tr ial or f rom interim analyses may suggest a change of entry cri teria . Changes

ma y a lso result f rom the discovery by monitoring sta f f that regula r violat ions of the ent ry

cri teria a re occurring, or that seriously low recrui tment ra tes are due to over-rest rict ive

cri teria. The protocol a mendm ent implementing such cha nges should cover an y sta t ist ical

consequences, such a s sa mple size a djustment s ar ising from dif ferent event ra tes, or

modif icat ions to the analysis plan.

11.2 Accrual rates

In studies with an appreciable t ime-scale for the a ccrua l of pat ients , the ra te of a ccru a l

should be monitored and, if i t falls appreciably below the projected level, the reasons should

be identi f ied an d remedial a ct ions ta ken in order to protect the power of the tr ia l a nd a l l a y

concerns about selective entry.

In a mult icentre t r ia l the a ccrua l ra te of pat ients at the va rious study si tes should a lso be

monitored to seek to ensur e that the cent res d o not diver ge excessively in the num bers of

patients entered (see Section 4.1).


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11.3 Checking the design assumptions

In large tr ials there wil l usual ly be an opportunity to check the assumptions which underlay

the origina l design a nd sa mple size calculat ions. This m a y be par t icularly importa nt i f the

tr ial speci f ica t ions ha ve been ma de on prel imina ry a nd/or uncerta in informa tion. An

interim check conducted on the bl inded dat a ma y reveal that overa l l response va ri a nces ,

event r a tes or survival experience a re not as a nticipat ed. A revised sa mple size ma y then be

calcula ted using sui ta bly modif ied a ssumptions, and should be just i f ied a nd documented i n

a protocol amendment and in the final report. The steps taken to preserve blindness and the

conseq uences, if any , for the type I err or a nd the widt h of confiden ce int erva ls should be

explain ed. The potent ia l need for re-estima tion of the sa mple size should be envisa ged in the

protocol whenever possible (see Section 5).

Substa ntia l di f ferences betw een the a nticipa ted and observed a verage level of the pri ma ry

variable(s) may pose addit ional design problems for a tr ial , because i t may al ter judgement

concerning the treatment difference to be detected, or the size of the non-negligible difference

to be excluded in the case of an equivalence tr ial . In addit ion, the val idi ty of an equivalence

tria l is judged by i ts simila ri t y to ear l ier tr ials of the posi t ive control, a nd substa ntia l

differences in the level of the primary variable do not support the idea of similarity.

11.4 Interim analyses and early stopping

When int erim a na lysis is plan ned, this is usua l ly a ccomplished by the use of a group

sequent ial design (see Section 4.5). The goal of such a n in t erim a na lysis is to stop the t ri a l

early i f the superiori ty of the trea tment under test is a lread y clea rly establ ished, i f the

demonst ra t ion of a relevant treat ment di f ference ha s become unlikely, or if una ccepta ble

adverse ef fects are apparent . The schedule of analyses, or at least the considerat ions whichwill govern its genera tion, should be sta ted in th e protocol or a ppended to it before the time of

the f irst int erim a na lysis ; the stopping rules and t heir propert ies should a lso be clea r ly

sta ted there. This mat eria l should be wri t ten or a pproved by the monitoring committ ee, w hen

the study ha s one. Devia t ions from the planned procedure a lwa ys bear the potential of

inva l ida t in g the study results . I f i t becomes necessar y to ma ke cha nges to the tr ia l , a n y

consequent amendments to the statistical procedures should be specified in the protocol at the

earliest opportunity. The procedures selected should always ensure that the overall type I

error i s , a t leas t , main ta ined .

The execut ion of a n inter im a na lys is must be a completely confiden tia l process beca use

unblinded data and results are potential ly involved. All staf f involved in the conduct of the

tria l should remain bl ind to the results of such a na lyses, beca use of the possibi li ty that th eir

a t t i tudes to the tr ia l wi l l be modif ied an d ca use cha nges in recrui tment pat terns or biases i n

treatment comparisons. This applies equal ly to the investigators and their staf f and to staf f

employed by the applicant. Investigators should only be informed about the decision to

continue or to discontinue the trial .

Any int erim a na lysis plann ed for a dminist ra t ive purposes only, wi th no ad justment of the

ty pe I error, should also be described in the protocol an d subsequ ently report ed. The purposes

of an a na lysis of this type should be clea rly sta ted, a nd should speci f ica l ly exclude a n y

possibility of ear ly st opping or other ma jor cha nges in design. The b lind should not be

broken .

Any unpla nned or incorrect interim a na lysis (with or without the consequence of st opping

the tr ial ear ly) ca n f law the results of a t r ial , a nd wea ken conf idence in the conclus ions


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drawn. Such analyses should therefore be avoided i f at al l possible . I f an unplanned interim

a na lysis cannot be a voided, the study report must lat er explain car eful ly why i t wa s

necessa ry, the degree to which bl indness ha d to be l i fted, a nd wha t result ing a ct ions w ere

possible in principle.

12. INTEGRITY OF DATA AND COMPUTER SOFTWARE

The credibi l i ty of the numerical results of the analysis depends on the qual i ty and val idi ty

of the methods and sof tware used both for data management (data entry, storage,

veri f ica t ion, correction a nd ret rieval) a nd a lso for processing the dat a sta t ist ical ly. D a ta

management act ivi t ies must therefore be based on thorough and ef fect ive standard operat ing

procedures (SOPs). The computer sof tware used for data management and stat ist ical

a na lysis must be completely rel iable , a nd documenta t ion of appropriat e va l ida t ion

procedures should be available. The computer systems and packages to be used should

preferably be identif ied in the protocol.

13. EVALUATION AND REPORTING

As sta ted in t he Int roduction, the str ucture a nd content of clinica l reports is the subject of

another note for guidance on Str uctur e and Content of Clin ical Study R eport s. This note for

guidance ful ly covers the reporting of sta t ist ical work, appropriately integra ted w ith cl in ica l

a nd other ma terial . The current section is t herefore rela t ively brief.

Dur ing the plan ning phase of a t r ial the ma in fea tures of the a na lysis should ha ve been

specified in an analysis plan and included in the protocol as described in Section 10. When

the conduct o f the t r i a l i s over a nd the data are assembled an d a vai l able for pre l im ina ry

inspection, i t is valua ble to ca rry out the blind review of the planned a na lysis a lso described

in Section 10. This pre-a na lysis review , blind ed to tr eat ment , should cover d ecis ion s

concernin g the exclusion of pat ients or da ta fr om t he a na lys is popula tion(s); possible

transformations may also be checked, and outl iers def ined; important covariates identi f ied

in other recent resea rch may be added to the model; the use of pa ra metric or non-pa ra met ric

methods ma y be reconsidered. Decisions ma de at this time should be described in reports,

and should be dist inguished from those made af ter the stat ist ician has had access to the

treatment codes, as bl ind decisions wil l general ly carry greater weight .

Ma ny of the more deta i led a spects of presentat ion a nd ta bulat ion, part icula rly of the less

cri t ical data, may be f inal ised at or about the t ime of the bl ind review so that by the t ime of

the actua l a na lysis ful l pla ns exist for a l l i ts aspects including patient selection, da ta

se lect ion a nd modi fica t ion , da ta summ a ry and ta bula t ion , es t imat ion a nd hypothesis

test ing. Once dat a va lida tion is complete, the a na lys is should proceed a ccord ing to the pre-

defined plans; the more these plans are adhered to, the greater the credibility of the results.

P ar t icula r a t t ention should be paid to an y di f ferences betw een the plann ed a na lysis a nd the

actual analysis , and a careful explanation should be provided.

All patients who entered the trial should be accounted for in the report, whether or not they

ar e part of an a na lysis populat ion. All r easons for exclusion from a na lysis should be

documented; for any patient included in the intention-to-treat population but not in theper-protocol populat ion, the rea sons for exclusion from the la tt er must a lso be document ed.

Sim ila rly, for al l pat ients included in an a na lysis populat ion, the mea surements of a l l


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importa nt var iables should be a ccounted for a t al l releva nt t ime-points . Furth er av a i la ble

informa tion on a ddit iona l pat ients screened for entr y but not ra ndomised should a lso be

summarised (see Section 10.1).

The ef fect of a l l losses of pat ients or dat a, wi t hdra wa ls f rom treat ment and ma jor protocol

violat ions on the ma in a na lyses of the prima ry va ria ble(s) should be considered ca ref ul ly .

Pat ients lost to fol low up or withdrawn from treatment should be identi f ied, and a descriptive

a na lysis of them provided, includin g the reasons for t heir loss a nd i ts relat ionship to

treatment and outcome.

Descriptive sta t ist ics form a n indispensable pa rt of reports . Suita ble ta bles a nd/or gr a phica l

presentat ions should i l lustrate clearly the important features of the primary and secondary

va ria bles and of key prognostic a nd demogra phic va ria bles. The results of the m a in

a na lyses rela tin g to the objectives of the tr ia l sh ould be the subject of pa rt icular ly ca re fu l

descriptive presenta t ion.

Although the prima ry goal of the a na lysis of a cl inica l tr ia l should be to a nsw er thequestions posed by i ts ma in objectives, new q uestions ba sed on the observed da ta ma y w ell

emerge dur ing the unbl inded ana lys is . Addi t iona l and perha ps complex s ta t i s t i ca l a na ly s i s

may be the consequence. This additional work should be strictly distinguished in the report

from work which was planned in the protocol .

The play of chance m a y lead to unforeseen imba la nces betw een the treat ment groups i n

terms of bas el ine measur ements not pre-def ined a s cova ria tes in the a na lysis plan but

ha ving some prognostic import a nce nevertheless. This is best deal t wi th by showing that a

subsid ia ry a na lys i s which accounts for these imbala nces reaches essent ia l ly the sa me

conclusions as the planned analysis . I f this is not the case, t

Metodologia estatística em pesquisa clínica

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